Post on 29-Jan-2021
Policy Research Working Paper 8476
Incentivizing School Attendance in the Presence of Parent-Child
Information FrictionsDamien de Walque Christine Valente
Development EconomicsDevelopment Research GroupJune 2018
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Produced by the Research Support Team
Abstract
The Policy Research Working Paper Series disseminates the findings of work in progress to encourage the exchange of ideas about development issues. An objective of the series is to get the findings out quickly, even if the presentations are less than fully polished. The papers carry the names of the authors and should be cited accordingly. The findings, interpretations, and conclusions expressed in this paper are entirely those of the authors. They do not necessarily represent the views of the International Bank for Reconstruction and Development/World Bank and its affiliated organizations, or those of the Executive Directors of the World Bank or the governments they represent.
Policy Research Working Paper 8476
This paper is a product of the Development Research Group, Development Economics. It is part of a larger effort by the World Bank to provide open access to its research and make a contribution to development policy discussions around the world. Policy Research Working Papers are also posted on the Web at http://www.worldbank.org/research. The authors may be contacted at ddewalque@worldbank.org and christine.valente@bristol.ac.uk.
Education conditional cash transfer programs may increase school attendance in part due to the information they trans-mit to parents about their child’s attendance. This paper presents experimental evidence that the information con-tent of an education conditional cash transfer program, when given to parents independently of any transfer, can have a substantial effect on school attendance. The effect is as large as 75 percent of the effect of a conditional cash transfer incentivizing parents, and not significantly differ-ent from it. In contrast, a conditional transfer program incentivizing children instead of parents is nearly twice
as effective as an “information only” treatment providing the same information to parents about their child’s atten-dance. Taken together, these results suggest that children have substantial agency in their schooling decisions. The paper replicates the findings from most evaluations of con-ditional cash transfers that gains in attendance achieved by incentivizing parents financially do not translate into gains in test scores. But it finds that both the information only treatment and the alternative intervention incen-tivizing children substantially improve math test scores.
Incentivizing School Attendance in the Presence of Parent-Child Information Frictions
Damien de Walque and Christine Valente*
JEL Codes: I25, D82, N37 Keywords: school attendance, conditional cash transfers, moral hazard.
*de Walque: Development Research Group, The World Bank, ddewalque@worldbank.org.Valente (corresponding author): Department of Economics, University of Bristol, christine.valente@bristol.ac.uk. The authors’ names are listed alphabetically.
Acknowledgements: We are extremely grateful for a fruitful collaboration with the Ministry of Education in Mozambique and in particular with Director Ivaldo Quincardete and all provincial authorities in Manica Province. This study is funded by the Results in Education for All Children (REACH), Strategic Research Program (SRP) Trust Funds, Research Support Budget (RSB) at the World Bank, as well as the International Growth Center (IGC). The data were collected by Intercampus, Lda with special thanks to Yolanda Chongo, Ana Lopes, Duelo Macia and Vitor Silva. The interventions were implemented by Magariro, with special thanks to Cecilia João, Celia Macuacua, Raul Maharate, and Mateus Mapinde. Nicola Tissi and Vicente Parruque provided expert field coordination assistance. We are grateful to Marina Bassi, Bruno Besbas, Fadila Caillaud, Peter Holland, Sophie Naudeau, Ana Ruth Menezes at the World Bank and Alberto da Cruz, Claudio Frischtak, Novella Maugeri, Jorrit Oppewal and Sandra Sequeira at IGC for their support and guidance. Last but not least, we are indebted to seminar participants and colleagues for their useful comments and suggestions. The findings, interpretations, and conclusions expressed in this report are entirely those of the authors. They do not necessarily represent the views of the World Bank, its Executive Directors, or the countries they represent. This research was approved by the University of Bristol’s School of Economics, Finance, and Management Ethics Committee on 14th March 2015. AEA registry trial ID number: AEARCTR-0001069. Initial registration date: February 29, 2016.
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Introduction Governments the world over strive to incentivize parents to ensure that
their children attend school regularly through subsidies, fines, and truancy laws
(BBC, 2005, Maynard et al., 2017). In developing countries, arguably the most
significant innovation in social policy in the past few decades has been the
introduction of conditional cash transfers (CCT) made to parents in order to
incentivize a number of prescribed behaviors such as regular school attendance,
and which are now implemented in over 60 countries (Parker and Todd, 2017).
When information frictions in parent-child interactions are taken into
account, however, simply providing information to the parent about child
attendance at school may improve attendance independently of any costly
transfer, and incentivizing children themselves may be more cost-effective than
incentivizing parents. While the role of children in their own schooling
decisions is generally ignored by researchers and policy makers, repeated
instances of peer effects in attendance decisions (Lalive and Cattaneo, 2006;
Cipollone and Rosolia, 2007; Bobonis and Finan, 2009) suggest that children
take part in decisions over whether they attend school (Kremer and Holla,
2009). In fact, when asked, a majority of surveyed children who have dropped
out of school by age 15 in India, Ethiopia, Peru and Vietnam say that they
themselves played the most important role in deciding to do so.1
In this paper, we provide experimental evidence from a poor, rural African
country setting that children have agency in decisions regarding their schooling
as early as sixth grade, and that neglecting this reality may lead to inefficiencies
in education policies. We present experimental evidence of the effect of three
alternative policies targeting Mozambican girls in the last two grades of primary
1 More precisely, 40% in India, 58% in Ethiopia, 65% in Vietnam, and 80% in
Peru. Authors’ calculations based on Young Lives Round 3 data (Boyden,
2014).
3
school: (1) providing weekly information to parents about their child's
attendance (information treatment); (2) providing this information and making
cash transfers to parents conditional on attendance – where the maximum annual
transfer is worth about 8 times the daily wages of an agricultural laborer or 7%
of per capita GDP (CCT treatment); or (3) providing the same information and
making transfers of the same nominal value to children in the form of a voucher,
also conditional on attendance (child incentive treatment). We draw three main
conclusions from our experiment. First, we find evidence that the information
content of a conditional transfer can have a substantial effect on school
attendance independently of any transfer. In our experiment, where the value of
the transfer is modest but similar to other CCT programs across the world,2 the
estimated effect of the information treatment on attendance is as large as 54%
of the child incentive treatment effect and 75% of the effect of the CCT
treatment. Our second key conclusion is that incentivizing children is at least as
effective in raising attendance as incentivizing parents – and importantly, not
because parents were able to appropriate the transfers made to children or
reallocate household expenditure to cancel out the transfer made to their
children.3 Finally, we replicate findings from most evaluations of CCTs that
gains in attendance achieved by incentivizing parents financially do not
translate into gains in test scores. In contrast, both the information treatment and
the children’s incentives treatment improve scores on the (ASER or “Annual
Status of Education”) math test by 8.5 to 9.4% of the control group’s mean. This
2 In their review CCT programs, Fiszbein and Schady (2009) state that transfers
range from no more than 4 percent of mean household consumption in
Honduras, Bangladesh, Cambodia and Pakistan to 20 percent in Mexico (p.5). 3Although we cannot reject the hypothesis that the parents incentives and
children incentives treatments had the same effect, the estimated effect of
incentivizing children is in fact 38% larger than the effect of incentivizing
parents.
4
suggests that improved attendance is beneficial for cognitive skills, but that
conditional cash transfers directed at parents may have counterproductive
effects, echoing findings by Baird, de Hoop and Özler (2013) that increases in
the monetary value of conditional transfers for which the household is eligible
increases adolescent psychological distress.
From a policy point of view, our results provide evidence of the
effectiveness of two lower cost, easily scalable, and, at least in the case of the
information intervention, arguably less politically controversial alternatives to
traditional CCTs: providing information to parents about their child's attendance
at school through a simple report card to be taken home at the weekend, and
incentivizing children with vouchers to be exchanged for a limited choice of
items which are likely to “stick” to their recipient such as school uniforms,
shoes, and school bags.
Our research contributes to three strands of literature. First, we augment
the knowledge base on intrahousehold decision making in the presence of
information asymmetry. A recent literature has emerged with the aim of
understanding the respective role of men and women and asymmetric
information between spouses in household decisions such as household
expenditure and family planning (Ashraf, 2009; Ashraf et al., 2014). But despite
recent work suggesting that children take part in household decisions (Dauphin
et al., 2011), recognizing that children may have their own preferences (Dunbar
et al., 2013), and finding that the investments in learning made by children age
10-14 are more important for test scores than those of their parents (Del Boca
et al., 2017), there is little evidence on the respective role of parents and children
in making schooling decisions – one of the key areas of decision affecting
children’s lives. Bursztyn and Coffman (2012) first showed that, in the presence
of asymmetry of information regarding school attendance between parents and
children, conditional cash transfers may be effective in increasing attendance in
part because they improve the parent's ability to monitor their child – at the very
least, a parent who receives a transfer conditional on 80% school attendance
5
should be reassured that her child has attended school at least 80% of the time.
Bursztyn and Coffman (2012) further find that parents in a poor urban Brazilian
setting indeed value the information component of a national CCT, but they do
not test empirically the effectiveness on school attendance or other outcomes of
providing information only, or how it compares to the effectiveness of providing
the conditional transfer as well as the information.
Several recent studies have investigated the effect of improving the
information parents receive about attendance (Berlinsky et al., 2017; Rogers and
Feller, 2018) and other measures of student effort at school (Bergman, 2016;
Bergman and Chan, 2017; Cunha et al., 2017) in urban, middle- to high-income
country settings.4 All find significant effects on attendance and, in three out of
4 Two of these papers explicitly compare the effect of providing information
about attendance to that of an encouragement for parents to ensure that their
children attend school regularly. Rogers and Feller (2018) compare the effect of
a reminder of the importance of regular attendance and of the parents’ role in
ensuring regular attendance with the effect of providing this reminder as well
as individual information about the child’s attendance record over the ongoing
academic year. They find that, while the reminder in itself reduces absences by
3.5%, the “reminder and attendance information” treatment reduces absences
by 6.9%, and that the two effects are statistically different from each other.
Cunha et al. (2017) compare the effect of text messages to parents about the
importance of school attendance, punctuality and assignment completion, with
that of text messages with information about the performance of their children
during the preceding 3 weeks on these three outcomes, but without reminder of
the importance of these behaviors. They find that both types of treatment have
similar effects. Taken together, these two studies suggest that reminding parents
of the importance of attendance and other behaviors can have an effect in itself,
and that the magnitude of this “salience” effect can be roughly similar to that of
6
five cases, on test scores as well (Bergman, 2016; Berlinsky et al., 2017; and
Cunha et al., 2017). The technologies used to transmit information to parents in
these studies (text messaging, email, post), although low-cost in a rich country
setting, would be difficult to implement if not unfeasible in many rural,
developing country settings such as the one we study. More importantly,
evidence of information frictions between parents and children in Santiago de
Chile, São Paulo, Philadelphia and Los Angeles do not necessarily translate to
rural Sub-Saharan settings – it is therefore striking for these studies and ours to
reach similar conclusions.5
A second strand of literature which our research complements is that on
the optimal design of cash transfers. Previous literature has, among others,
focused on the role of the conditionality (see Baird et al., 2014 for a meta-
analysis and Baird et al., 2011; Benhassine et al., 2015 and Akresh et al., 2016
for experimental comparisons of conditional and unconditional or “labeled”
transfers), varied the gender of the recipient (Benhassine et al., 2015; Akresh et
al., 2016; Haushofer and Shapiro, forthcoming), and studied the optimal timing
of the transfers (Barrera-Osorio et al., 2011). But little is known about the
effectiveness of incentivizing children vs. incentivizing parents. Two recent
providing information only. In our experiment, we only provided information,
and only information about the pupil’s attendance. 5 For conciseness, we focus here on the literature interested specifically in the
information asymmetry between parents and their children in the area of
education. Gallego et al. (2017) have documented evidence of information
asymmetry between parents and children regarding internet usage, and a rich
body of work has shown evidence of misinformation relevant to educational
choices that goes beyond parent-children asymmetric information (e.g.,
Nguyen, 2008; Jensen, 2010; Bettinger et al., 2012; Hoxby and Turner, 2013;
Dinkelman and Martínez, 2014; Wiswall and Zafar, 2015; Andrabi et al., 2017;
Dizon-Ross, 2017).
7
papers compare experimentally the effect of incentivizing parents relative to
incentivizing children to achieve an attendance (Baird et al., 2011) or
performance target (Berry, 2016). Baird et al. (2011) vary experimentally the
amount of cash given to parents (from $4 to $10) and that given to adolescent
girls (from $1 to $5) in Malawi and find similar effects for each extra dollar
irrespective of the nominal recipient of the cash transfer. It is however possible
that the cash given to the adolescent girl with the full knowledge of her parents
had to be, at least in part, devolved to the parent. In addition, the authors find
that increasing the value of the conditional transfer offer has no effect on the
outcomes studied over and above the minimum value of the conditional transfer.
In a context where increasing the amount of the transfer does not increase the
treatment effect, it is perhaps not surprising to find that the identity of the
recipient of the extra dollar does not matter. Our experiment does not split the
transfer amount between parent and children but varies who receives the transfer
altogether, and in order to ensure that our child incentive treatment indeed
incentivized the child, we chose to provide transfers to children in the form of
vouchers to be redeemed against a limited number of items that are both
attractive to the children and unlikely to be appropriated by others. Berry (2016)
compares the effect of a range of treatments – randomized across individuals –
incentivizing the performance of Indian children in Grades 1 to 3 on a literacy
test, varying the type of transfer (cash, voucher to buy toys, toy) and recipient
(parent or child). He finds no evidence that the identity of the recipient matters
on average, but sheds light on how the recipient of the performance incentive
scheme may interact with the relative productivity of parents and children in
producing learning. Our paper instead focuses on the effect of incentivizing
children who are older (and thus possibly more likely to have agency in
schooling decisions) simply to attend school, and hence abstracts from issues of
relative parent/child efficiencies in learning production in order to provide a
direct test of the importance of parents’ and children’s returns to education in
attendance decisions.
8
Finally, we offer new light on two puzzles arising from experiments
evaluating the effect of education subsidies in developing countries. The first of
these puzzles is that most studies evaluating the effect of CCTs (to parents) on
test scores estimate positive effects on enrollment and/or attendance but find no
evidence of gains in test scores (with the notable exceptions of Barham,
Macours and Maluccio, 2016 and Baird et al., 2011). While this lack of evidence
of cognitive skills gains can be rationalized in part by sample selection issues –
in studies using school-based tests, children induced to attend by the CCT may
have lower skill levels– and/or school quality being negatively affected by
increased school participation, we replicate this finding using data from a
sample of eligible children who are not selected based on school attendance and
largely ruling out the worsening school quality mechanism. Indeed, we find that
our other two interventions have effects on attendance of the same order of
magnitude as the CCT, but have positive effects on test scores an order of
magnitude larger than the CCT. This finding points to the conclusion that
introducing parental incentives on attendance produces specific negative
spillovers on learning. The second well-known puzzle arising from previous
research on which we shed new light is that simply distributing free school
uniforms has had large effects on attendance, enrollment, and pregnancy
outcomes in Kenya (Duflo et al., 2015 and Evans and Ngatia, 2017), which, as
noted by Kremer and Holla (2009), is difficult to reconcile with simple models
of human capital investment where decisions are solely made by parents.6,7
6 In urban Ecuador, Hidalgo et al. (2013) find that a program of free school
uniforms decreases attendance, which they argue may be due to a combination
of factors including the fact that only 63% of schools where children were told
that they would receive free uniforms actually did. 7 Examples of ITT (LATE) effects reported in these studies are: 3.8 (7.0) %-
points or 20 (37)% decrease in absenteeism in Evans and Ngatia (2017), and
9
Even if not conditional on an attendance target, it is reasonable to think of the
receipt of free, new, school uniforms as increasing children’s returns to school
attendance in addition to decreasing out-of-pocket costs for parents. If
children’s returns to education matter for schooling decisions independently of
the value parents attach to this education – as we find supportive evidence for
here, then the increase in children’s benefits to school attendance could explain
part of the large effects observed.
In the remainder of the paper, we present the study context, theoretical
motivation for, and design of our experiment (Section I), then turn to a
description of the data and randomization process (Section II), before reporting
our main results (Section III) and various robustness checks (Section IV).
Section V concludes.
I- Institutional Context, Theoretical Motivation and Study Design
A. Institutional Context
Mozambique is a predominantly rural country in South-Eastern Africa
(68.4% of the population lives in rural areas, INE 2015) and, with a Human
Development Index ranking 181 out of 188 (Kenya, for instance, is ranked 146),
is one of the poorest countries in the world despite a doubling of real GDP per
capita between 2001 and 2016 (from $615.3 to $1,128.3 PPP, World Bank
2017). The country’s recent history has been marked by a 15-year civil war
following independence in the 1970s, and occasional clashes between armed
forces and RENAMO’s armed militias in the center of the country. Despite large
increases in enrollment rates in lower primary school grades, most children are
still not completing primary education. As of 2014, the net enrollment rate in
primary education was 87.6%, up from 54.8% in 2002. But the survival rate to
16.5 (18.9)% decrease in female (male) primary school drop out after three
years in Duflo et al. (2015).
10
the last grade of primary education was only 33.2% in 2013, compared to a Sub-
Saharan average of 57% (World Bank Education Statistics Data Bank, 2017).
While the net intake at Grade 1 of primary schooling is high for both boys
(74.5%) and girls (73.1%), and secondary schooling is still restricted to an elite
(17.9% net enrollment for both boys and girls), most children in Mozambique,
and girls in particular, experience difficulties in completing primary school.8
For upper primary schooling (Grades 6 and 7 or Ensino Primário de Segundo
Grau “EP2”, which the present study focuses on), the official completion rate is
abysmal, especially in rural areas where even at age 19 it is only about 14% for
males and 8% for females (according to Figure 3.10 in Fox et al., 2012). In this
context, a policy priority is to find ways to increase the school attachment of
pupils, and girls in particular, in the higher grades of primary school.
We focused on one province of Mozambique where our implementation
partner – the development NGO Magariro – is active and well-known: Manica.
Manica Province is located in the Center Region of Mozambique and is home
to 7.5% of the country’s population. It is close to the national average on a
number of indicators, from population density (30.3 people per square meter
compared to a national average of 31.3), poverty rate (41% in 2014 compared
to a national average of 46.1%), to annual drop-out rates in primary schooling
(6.8% in Manica and countrywide for EP1, 9.9% versus 8.8% nationwide for
EP2) (INE, 2015; MPD-DNEAP, 2016). Mozambique in general, and Manica
Province in particular, have low population density even for Sub-Saharan Africa
standards (where the average was 42.6 in 2015), but not dissimilar to other
countries in Eastern Africa (36.7% in Kenya, for instance). This may matter in
our context because our study design is, as explained below, motivated by the
hypothesis that there may be imperfect monitoring of the children’s actions by
8 The net intake equals the ratio of the total number of pupils in Grade 1 of the
official starting age (6) divided by the number of children age 6. All figures are
taken from World Bank Education Statistics Data Bank (2017).
11
parents, which is plausibly more likely when population density is low and the
school is located further away from the child’s home.
B. Theoretical Motivation
One key policy tool used to improve school enrollment and attendance
rates in today’s developing world is cash transfers, which are often conditional
on attendance and other prescribed behaviors. While they have been
implemented in over 60 countries (Parker and Todd, 2017), there are several
unanswered questions about this type of social transfers.
One highly debated question is that of the role of conditionality. If the
only reason why individuals do not invest more in human capital is that they
face credit constraints, then unconditional and conditional cash transfers should
have a positive effect on human capital investments irrespective of the
conditions attached to the transfer. On the other hand, conditionality may lead
to larger increases in school enrollment, e.g. if individuals underestimate returns
to education or if the conditionality helps parents monitor their children’s
behavior, since they can infer whether their child attended school regularly from
the transfers they receive or do not receive. The first argument in favor of
conditionality (underestimation of returns to education) is well-known. The
second, however, has appeared only recently in the literature, and has been
shown to be very relevant in the Brazilian urban context, where parents have
been found to value the monitoring of their children’s attendance at school
(Bursztyn and Coffman, 2012). The idea is simple, and is rooted in the well-
known critique to Becker’s (1974) “Rotten Kid Theorem”. Becker (1974) shows
that an altruistic parent can incentivize his/her child to do what is optimal
according to the parent. Therefore, from a policy maker’s point of view, it
suffices to incentivize the parent to achieve a desired outcome such as school
attendance. Bergstrom (1989) however demonstrates that the theorem does not
necessarily hold in the presence of moral hazard. Bursztyn and Coffman (2012)
show, both theoretically in a simple principal-agent model with moral hazard,
12
and through a lab experiment in the case of the Brazilian education CCT
program Bolsa-Escola, that the conditionality may reduce information
asymmetry and thus reestablish the conditions for the theorem to hold.
Bursztyn and Coffman’s (2012) point can be summarized as follows.
Consider the parent-child pair indexed by n for whom adult utility is:9 1
0 0 (1) Where indicates whether the child chooses the high or low effort action
(here, attending school or not), and the child’s utility is:
10 0 (2)
Where is the utility cost of effort experienced by the child. is the benefit the adult derives from the child’s education, net of costs.
If , the child attends school even without further incentives, irrespective of the parent’s ability to monitor her attendance. If , then it is optimal for the child not to go to school from the point of view of
maximizing the sum of the payoffs of the parent and child, irrespective of the
parent’s ability to monitor her attendance. If, however, but , then whether or not it is optimal for the parent to incentivize the child to go
to school depends on the quality of the parent’s monitoring technology. Define
the signal technology as:
Pr 1| 1 Pr 0| 0 , ∈ 12 , 1
9 Note that the discussion extends to the case where the payoffs associated with
education are only received with probability p
13
A parent can only condition transfers to the child based on signal ,
which is correct with probability .10 Assuming limited liability on behalf of the child, the adult will find it optimal and feasible (i.e., incentive-compatible
from the child’s point of view) to incentivize the child only if:11
(3)
Where the probability of inequality (3) holding increases with signal
quality (higher . As a consequence, under imperfect information, simply
providing information to the parent may induce higher attendance. Since CCTs
give the parent, at a minimum, a binary signal as to whether or not the child met
the attendance requirement upon which payments are conditioned, the
conditionality may in itself lead to higher attendance. This motivates our test of
whether giving parents information about their child’s attendance has an effect
on attendance. In addition, it motivates our test of the extent to which the effect
of giving this information and nothing else differs from that of a CCT program
providing the parents with the same information as part of the program.
In addition, we make the observation that, under imperfect information,
incentivizing the child should be more cost-effective than incentivizing the
parent because of the informational wedge . Indeed, increasing by some
transfer t makes inequality (3) more likely to hold than increasing by the
10 When is just larger than , there is close to no information contained in the
signal since the parent’s inference is only marginally superior to a random
guess, while the case 1 corresponds to the full information case. 11 Denote the transfer made by the parent to the child if 1 and the minimum payment such that the child’s expected payoff is at least as large when
1 than when 0. Condition (3) is obtained by maximizing the adult’s utility subject to the incentive compatibility constraint and the limited
liability constraint 0.
14
same amount (since 1).12 This motivates our comparison of the additional effect (relative to improving information only) of conditional
transfers aimed at parents to that of conditional transfers aimed at children.
C. Study Design
In order to assess the relevance of our analytical framework, as well as to
help define the design of the Randomized Controlled Trial (RCT) described
below, we first undertook a qualitative analysis in the province where the RCT
took place but in areas that were not included in the trial. The information
gathered during focus group discussions with parents and (separately) with their
daughters age 11-15 gives support to the hypotheses that (i) both parents and
girls of this age have an influence on school attendance decisions and (ii)
children have private information on their school attendance. In addition, data
collected in the baseline household survey in the experimental sample asked
parents (both in treatment and control areas) whether they thought it would be
useful to see a weekly report showing whether their daughter had attended
school regularly, and, if they answered that it would, a follow-up, open-ended
question then asked why they thought such report would be useful. Eighty
percent of parents responded “yes” to the first question, and among those, when
asked (the open-ended question of) why they thought it would be useful, 98%
responded that it would allow them to monitor their child’s school attendance.
Other than providing a first pass confirmation of the relevance of our
analytical framework to the study area, the preliminary focus groups aimed to
establish how to incentivize girls effectively and in a manner that would be
acceptable to the local population. The main conclusions were that giving cash
12 And the effect of incentivizing children should be all the larger than that of
incentivizing parents the larger the informational wedge. A CCT which
improves parental information such as ours should therefore lead to a reduction
in the additional effectiveness of incentivizing children relative to parents.
15
to girls would make both the girls and their parents uncomfortable, that if they
did receive cash they would give it to their parents (or be expected to), but that
there were a number of items which, if given to them to reward school
attendance, would be welcome by the girls and likely to “stick” to them.
Given these insights, we designed the following four experimental groups.
In two of the experimental groups, we introduced transfers conditional on
achieving at least 90% attendance during the school trimester. In a “girl
vouchers” treatment arm, we gave money-equivalent vouchers (400 meticais13
at the end of each trimester with a maximum of 1,200 meticais over the 2016
school year) to girls in Grades 6 and 7 who could then use the vouchers to buy
a selected number of items such as: school uniforms, shoes, school bag, smaller
materials (pens, notebooks, etc...), which were delivered at the school by the
research team and could be purchased during the research team visit. The choice
of items made available was based on the preliminary focus group interviews
carried out in villages outside the study area. The qualitative evidence collected
indeed suggested that these items met two important criteria: (i) they were
consistently cited when children (parents) were asked what gifts could
incentivize them (their daughters) to attend school regularly and (ii) both parents
and children seemed confident that a girl who was given these items would be
able to keep them for herself and would not be expected to share with anyone
else. In a “parents cash” treatment arm, we instead gave the same value (400
meticais per trimester) in cash to the parents and made the same items as in the
“girl vouchers” arm available for optional purchase at the school. It was clearly
explained that there was no expectation as to how the parents would spend the
13 400 Mozambican meticais was worth US$8.36 on January 1, 2016 but only
US$5.62 on December 31, 2016, as the exchange rate deteriorated substantially
over the course of the (school) year. The maximum annual transfer is worth
about 8 times the daily wages of an agricultural laborer in the study area.
16
money, and the items were available for purchase at a short distance from the
desk at which the cash was distributed to avoid pressurizing the parents.
Note that, in addition to matching the value of the vouchers given to girls
to the cash received by parents, the price of items in vouchers matched the price
in Mozambican meticais to reinforce comparability. In both conditional
transfers arms, the conditionality was enforced by the implementing NGO based
on the information contained in attendance report cards distributed at the start
of the trimester. These simple report cards (a sheet of paper inside a plastic
pocket) had a coding easily understood by parents: the teacher drew a circle for
a given day if the girl attended school that day, or the teacher marked a cross
for each day missed. The report cards were given to the girls at the end of each
week to show their parents and brought back to school at the start of the next
week. The report card system was explained by the implementing NGO during
a visit to the school community before the intervention. Parents, either through
direct attendance at this initial meeting, or through learning about the report card
system from other parents, teachers, or pupils, could draw their own conclusions
if a child decided not to show the parent the report card. All girls enrolled in
EP2 in the conditional transfer schools were eligible for transfers and thus given
attendance report cards.
In a third treatment arm, we applied an "information" treatment, in which
we introduced the report card system described above, but where attendance
was not incentivized by vouchers or cash transfers. A fourth experimental group
constituted the control group.
A comparison of school attendance rates between the information
treatment group and the control group answers the question of the effect of
reducing the information asymmetry between children and parents. The
inclusion of the information treatment group allows us to disentangle the effect
of providing information to parents on their child’s attendance from that of
increasing parental (in the “parent cash” arm) or children’s (in the “children
vouchers” arm) returns to attendance.
17
In order to ensure the quality of the data recorded in the attendance report
cards,14 and given the extra work required from the main teachers (“Directores
de Turma”) to fill in those cards, we introduced a small compensation scheme.
The scheme worked as follows: in the three intervention groups, the main
teachers in charge of a class who, at every spot check by the independent
surveyor, were found to have thoroughly filled in all their (female) pupils’ report
cards for the current trimester until the day of the spot check, received 250
Meticais’ worth of airtime at the end of the trimester. The value of 250 meticais
corresponds to the opportunity cost of about 5 minutes per day, evaluated at the
hourly salary equivalent of the average teacher. The school directors of all
schools, including the control group, received 250 meticais in airtime at the end
of each trimester without conditions to thank them for their assistance and cover
small costs due to necessary communications with the research team.
II- Data, Randomization and Experimental Balance A. Data
Independent, unannounced, attendance checks (“spot checks”). The main
outcome of interest for the evaluation is whether a girl enrolled in school was
present during independent attendance “spot checks” by the survey firm hired
by the authors. Twice per trimester, an enumerator arrived unannounced at each
school in the sample and recorded in person the individual attendance/absence
14 A systematic review by Baird et al. (2014) of conditional versus unconditional
transfers shows the importance of enforcing conditionality. The review indeed
concludes that CCT programs that are explicitly conditional, monitor
compliance and penalize non-compliance have substantively larger effects than
unconditional transfers (60% improvement in odds of enrollment), whereas the
advantage of CCTs with minimal monitoring and enforcement over
unconditional cash transfers is not clear.
18
of every child enrolled in EP2. The attendance rate triggering transfers in the
conditional transfers arms was calculated by the implementing NGO solely
based on the information contained in the attendance report cards described in
Section I-C. No incentive was paid on the basis of the presence or absence of
pupils during the attendance spot checks and therefore there is no reason to
expect the data to be manipulated. In addition, the enumerators were blind to
the treatment arms, so that there is no reason either to expect the data to be
affected by social desirability bias.
In addition to the spot check data, a baseline household survey and an
endline household survey collected basic household information as well as, for
each girl in the household who had completed, at least, 5th Grade, and, at most,
6th Grade, as of the end of 2015 (and was therefore potentially eligible for the
conditional transfers): data on self-reported quality of attendance monitoring by
the parent or guardian, degree of agreement about statements regarding returns
to education for each child, self-reported girl empowerment, expenditure on
personal goods consumed by the eligible girl, cognitive tests (at endline only),
and household expenditure data (at endline only).
Household survey sample. The household data used in the analysis is
based on a sample drawn from the universe of girls enrolled in the 173 schools
included in our study within three years of the data collection (based on school
records), as in Benhassine et al. (2015), and who still lived with their parent or
guardian at baseline (given our analytical framework based on asymmetric
information between parents and children). The target was to interview 20
potentially eligible girls per school, sampling those enrolled in 2015 (the last
academic year before the trial) and recent drop outs who were not enrolled in
2015 but were enrolled in 2013 or 2014, proportionally to the size of each of the
two groups (“enrolled in 2015” and “recent drop outs”) in the school.15 During
15 Ahead of the baseline survey, the survey team visited each school and, based
on school records, drew the list of all girls who (i) were enrolled in grade 5 or
19
fieldwork, however, there were difficulties locating the girls listed in the school
records, and most of the recent drop outs had either moved away or were not
living with their parents anymore and were thus ineligible for interview. The
sampling target of 20 per school was therefore not attained in many of the
smaller schools, and where possible more than 20 girls were sampled in order
to help preserve power. All in all, the median number of girls surveyed per
school in the baseline household survey is 18, and recent drop outs were under-
represented in the household survey sample (3% of the baseline sample
compared to 13% of all girls last enrolled in Grades 5 or 6 at some point during
2013-2015 across all 173 schools). There was no difference in the total number
of girls interviewed in the baseline household survey, or the share of recent drop
outs in the household survey sample, across treatment arms, however.16 For
transparency, the main analysis reported in this paper is carried out at the school
level (i.e., averaging variables at the school level), and does not apply any
sampling weights so that each school is weighted equally whatever the number
of girls interviewed or observed during the spot checks. In robustness checks
reported in Section IV, we also repeat the analyses giving each school a weight
proportional to the size of its potential EP2 intake for 2016 (based on school
enrollment data for 2013, 2014 and 2015 and thus prior to our experiment).
Timing. The Mozambican school year runs from February to December.
We collected a baseline survey between the end of the 2015 school year and the
start of the 2016 school year, and a follow-up survey one year later (See Figure
1). Each school received an initial visit by the implementation NGO, a locally
well-known development organization called Magariro. School staff in all
grade 6 in 2015 (“enrolled in 2015” list) or (ii) were enrolled last in grade 5 or
6 either in 2013 or 2014 (“recent drop-outs” list). 16 The maximum difference between any two experimental arms is 0.8 girl (t-
stat: 0.72) for the number of girls interviewed and 1.4%-points difference in the
share of recent drop outs (t-stat: -1.26).
20
schools were invited to an information meeting in which they were informed
that there would be unannounced visits by the survey firm to independently
collect attendance data between one and three times per trimester throughout
the school year. In treatment schools, the initial meeting was also open to pupils
and parents of the relevant grades, and the relevant intervention was explained,
attendance report cards distributed to the school, and questions answered. The
intervention started at the beginning of the 2016 school year (February 5) or as
soon as the treatment was announced, if announced after the start of the
academic year, which was the case for the vast majority of schools. Re-
enrollment is automatic for grades such as Grade 7 at which admission is not
conditional on passing an exam. In the case of Grade 6, in which enrollment
requires students to have passed the end of Grade 5 exam, re-enrollment is not
automatic but the official enrollment period ended on January 6, 2016. The
treatment announcement visits by the implementing NGO started on January 14
and ended on March 3. Initial visits by Magariro to announce the treatments
took place after the start of baseline survey collection in all but one school. But
given the delays in completing the baseline survey caused by political tensions
between RENAMO and government forces and by heavy rains, in just under
22% of schools, the baseline survey was completed after the initial visit in which
the NGO announced the treatments.17 This may have affected baseline self-
reported attendance and monitoring quality, but there is little reason to believe
that it should have affected data on baseline socioeconomic indicators or any
17 There is, however, no statistically significant difference in the timing of the
treatment announcements across treatment arms relative to the average baseline
household interview date. More precisely, when regressing the number of days
between treatment announcement and average household interview dates on
two treatment indicators (where the third treatment is the omitted category) and
a set of district fixed effects, the p-value of a joint F-test of significance of the
two treatment coefficients is 0.54.
21
other variable for which we test balance at baseline. The interventions were not
means-tested, and more generally there was no room to manipulate the
eligibility criteria (gender and grade). In all schools, the treatments were
announced after the official enrollment period and, in three quarters of schools
(corresponding to 7 out of 11 districts), well after the start of the new school
year, so these announcements were unlikely to affect enrollment decisions,
especially considering the likely delay in spreading information to the parents
of marginal enrollees.18
Table 1 presents the allocation of schools and girls across the four study
groups as well as the attrition rate for girls sampled for the household survey.
While attrition of girls taking part in the household sample was limited at 5.3%
overall, it was slightly larger in the control group than in the treated groups.
Robustness checks reported in Section IV show that this differential attrition is
unlikely to be driving our conclusions. Our main outcome of interest
(independently verified attendance rate at school), however, is available for all
schools between one (for 3 schools) and 6 times (for 132 schools), and on
average 5.6 times during the school year - corresponding to 5.6 spot checks on
average, and the number of times each school was surveyed is independent of
experimental arm (the p-value of a joint FF-test is 0.55).
18 There is no statistically significant difference in the timing of the treatment
announcements across treatment arms relative to the start of the academic year.
More precisely, when regressing the number of days between treatment
announcement and the start of the academic year on two treatment indicators
(where the third treatment is the omitted category) and a set of district fixed
effects, the p-value of a joint F-test of significance of the two treatment
coefficients is 0.72.
22
B. Randomization and Experimental Balance
We first stratified our sample of 173 schools by district to avoid randomly
occurring imbalances across experimental arms in district characteristics, in
fieldwork operations (since these were organized district by district), as well as
to gain power, since educational outcomes vary across the 11 districts of Manica
province (see, e.g., p.24 in MINEDH 2017). We then split the schools included
in our study, within each district, randomly between the four experimental arms
(one control and three treatment arms) using a random number generator.19 At
the time of the announcement of the treatments, a human error led to two schools
in the Vanduzi district being swapped (one in the information treatment and one
assigned to the parent cash treatment). Throughout this paper, we classify each
school based on their randomly assigned treatment arm, but our findings are
robust to assigning treatment based on actual treatment status instead of
intended treatment status.20
19 In districts where the number of schools was not a multiple of four, one of
two rounding rules was first selected at random to determine the number of
schools to assign to each experimental group before assigning schools randomly
to experimental arms. Rounding rule 1 stated that the number of schools in the
control group should be rounded up, and that in both conditional transfers arms
be rounded down. Rounding rule 2 stated that the number of schools in the
control group should be rounded down, and that in both conditional transfers
arms be rounded up. The residual experimental arm was the information
treatment arm, which explains that slightly fewer schools fall in this
experimental arm (41 compared to 44 in all the other arms). For instance, in the
Vanduzi district, where there are 21 schools, the randomly selected rounding
rule was rule 2, resulting in 6 “parent cash”, 6 “girl voucher” schools, 5 control
schools and 21-17=4 “information” schools. 20 Full results available on request.
23
Table 2 presents summary statistics for all the socioeconomic indicators
measured in the baseline survey and characteristics of the eligible girls and self-
reported monitoring technology relevant to our research framework, by
treatment arm, as well as whether p-values of t-tests of differences between each
treatment arm relative to the control group indicate that those differences are
statistically significant.21 Table 2 suggests that the randomization of
experimental arms worked well in practice. For each pair of experimental arms,
an F-test cannot reject that the baseline characteristics listed in Table 2 are
jointly orthogonal to treatment status.22 Some individual differences are,
however, statistically significant, and thus we provide robustness checks
controlling for these baseline characteristics. Note that other than for the many
language and religion categories, for which there are some differences across
experimental groups, the only other variables with some significant baseline
differences between experimental arm pairs are self-reported absences and, to a
marginal extent, self-reported quality of child attendance monitoring by the
parents. Given the direction of the differences (parents in conditional transfers
arms reporting fewer child absences), this may well be due to the fact that, in
about one fifth of the schools, the baseline survey could not be concluded before
the treatments were announced, so that parents in conditional transfers arms
may have been tempted to underreport child absences.
21 These p-values are those associated with a t-test of 0, 0 and 0 respectively, obtained from estimating Equation (4) with each baseline characteristic, in turn, on the left-hand side. 22 More specifically, the p-value associated with an F-test that the set of
characteristics listed in Table 2 does not explain the experimental arm
classification is between 0.17 (Information v. Parents) and 0.52 (Control v.
Girls) for all 6 experimental arm pairs, and thus the null of joint orthogonality
cannot be rejected.
24
III- Main Results In this section we report and discuss cluster-level estimates based on
Equation (4) below:
(4)
Where is the cluster (i.e., school) average for outcome ; , and are indicator variables for the girls, parents, and information only treatment
arms, respectively; is a row vector of 10 district (i.e., strata) fixed effects (as
there are 11 districts), and is an iid error term.
, , and can be interpreted as average treatment effects for our sample of 173 schools, giving each school an equal weight, or unweighted
average treatment effects. As noted by Athey and Imbens (2017), analyzing the
data at the cluster level in cluster-randomized experiments is both transparent
and appealing because all the estimation formulas obtained for simple (as
opposed to cluster-) randomization apply directly. In Section IV, we report
estimates giving each school a weight proportional to its relative size, as
predicted by pre-treatment enrollment in Grades 5 and 6, to speak to the
population average treatment effect.
Table 3 presents estimates of the impact of the different interventions on
schooling outcomes. In Columns (1) and (4), we report findings for our primary
study outcome, i.e., school attendance measured as the share of girls in the
targeted grades who were found in their classroom by the independent surveyor
during unannounced school visits. The two columns present the cluster level
analysis (Equation (4)) with and without controlling for the (school average)
baseline characteristics listed in Table 2 for which a t-test rejects equal means
at baseline for at least one treatment arm.
Compared to the control group, all three interventions significantly and
substantially increased school attendance. Compared to a control group mean
of .65, the report card treatment increased attendance by 4.5 percentage points
25
(6.9%), the parent cash treatment increased attendance by 6 percentage points
(9.2%), and the girl voucher treatment increased attendance by 8.3 percentage
points (12.8%). The p-values reported at the bottom of the table show whether
the coefficients for each of the three interventions are statistically different from
each other. The first row of p-values indicates no significant difference in
impacts between the information only (report card) and the CCT (to parents)
interventions. This leads to the conclusion that the information content of a
conditional transfer program can have a substantial effect on school attendance
independently of any transfer – in our experiment, where the value of the
transfer is relatively small at 7% of GDP (but comparable to a number of
existing CCTs), the estimated effect of the information treatment on attendance
is as large as 75% of the effect of the CCT. In addition, the estimated effect of
the information treatment on attendance is as large as 54% of the effect of the
child incentive program. Incentivizing girls directly is nearly twice as effective
as simply providing information, and in our baseline specification (Column (1)),
this difference is statistically significant at the 10% level. The experiment lacks
power to detect a genuine difference between the parents and child incentive
treatments, but the estimated effect of incentivizing children is as much as 38%
larger than the effect of incentivizing parents.
One concern in interpreting any difference in the effect of the “girl
voucher” and “parent cash” treatments is that of whether the transfers were
indeed received by the targeted individuals: if girls were unable to retain the
transfers aimed at them, then there would be no practical difference between
nominally incentivizing the parent or the child. Our finding that incentivizing
children is at least as effective as incentivizing parents is particularly interesting
in the light of evidence that our children transfers “stuck” to the targeted child.
First, when asked at endline, no surveyed girl from the girl voucher arm
responded that she had given away her reward or had had to sell it to give the
26
money to someone else.23 Second, it could have been the case that parents
substituted away from expenditure on the type of goods obtained by the girl
through the voucher system, thus neutralizing the transfer to the girl. We
collected detailed information on the girls’ consumption of (23) personal items
such as clothes, bags, soap, books, etc…, excluding any item purchased through
a voucher, to test for this. While we found – unsurprisingly given substitutability
– a negative effect on consumption of personal items other than those purchased
with the voucher in the girl voucher treatment compared to the control group,
this effect was statistically insignificant and small relative to the amounts
transferred (89 Meticais compared to an average of 469 meticais received in
vouchers, on average, see Table A-1).
In Column (4) of Table 3, we present results obtained when controlling
for the baseline characteristics for which there was at least one statistically
significant difference between experimental arms and confirm that results are
virtually unchanged.
Column (2) reports results on the effect of our treatments on school
enrollment as reported by parents in the household survey. Starting from a high
enrollment rate (95% in the control group), and given the fact that the
intervention was announced after the end of the official enrollment period (and,
in most cases too, after the start of the school year), it is not surprising to confirm
that our interventions had no effect on enrollment decisions. The CCT seems to
have had a small impact in increasing enrollment by 2.7 percentage points in
the baseline specification, but when controlling for baseline characteristics
(Column (5)), the point estimate decreases and a t-test cannot reject the null of
no effect (p-value: 0.21). Based on this and further tests showing that the effect
on enrollment is not robust (Section IV), we conclude that the effect on
enrollment was negligible.
23 Of 101 girls chosen at random among the “girl voucher” survey sample to
answer this question.
27
Rigorous evidence of the effect of conditional cash transfers (to parents)
on test scores is limited. This evidence is generally based on school data and
thus potentially affected by selection into school attendance at the time of the
test (Saavedra, 2016). Most studies find no evidence of test scores gains. The
two exceptions that we are aware of are Barham, Macours and Maluccio (2016),
who find positive effects for boys in Nicaragua, and Baird et al. (2011) who find
positive effects for girls in Malawi. In columns (3) and (6), we provide estimates
based on test scores at a math (ASER) test administered to eligible girls in our
endline household survey, irrespective of attendance at school, which are
therefore not affected by the type of selection bias which may undermine test
scores effect estimates from CCTs based on school tests. Similar to most
previous evidence, we find that gains in attendance from cash incentives to
parents do not translate into gains in test scores. On the contrary, both the
information treatment and the girls' incentives treatment improve math scores
by 8.5 to 9.4% of the control group’s mean.
While the girls’ incentive treatment has a larger effect on attendance than
the information treatment, the effect of both treatments on test scores is of
similar magnitude and statistically significantly larger than in the parent CCT
arm. It could be that part of the effect on test scores of the information treatment
stems from something else than more regular school attendance. Prompted by
the realization of their imperfect attendance monitoring technology, parents in
the information treatment may plausibly increase their monitoring of other
aspects of schooling effort such as homework, and do so more in the information
only treatment where imperfect monitoring may at first be more salient than in
the transfers treatments.24 Or the similar magnitude of the effects on math scores
24 It may indeed take parents more time to realize the informational content of
the attendance report in the transfers arms, where it fullfils the additional
function of allowing verification of the condition, than in the information only
arm. Consistent with this, the effect of the information treatment has a flatter
28
of the information only and girl voucher treatments may simply be due to the
coarseness of the math scores, which can only take five possible values, from 0
for girls who cannot even correctly identify single-digit numbers to 4 for girls
who can correctly perform divisions with remainders.
More importantly, while the effect on attendance of the girls’ incentives
treatment was larger in magnitude but not statistically different from that of the
CCT, the effect of the girls’ treatment on test scores is 10 times larger (and
statistically significantly so) than the effect of the CCT. Taken together, this
evidence suggests that CCTs directed at parents may have counterproductive
effects. Baird, de Hoop and Özler (2013) find that, while eligibility for cash
transfers (be it conditional or unconditional) reduces adolescent psychological
distress at the extensive margin, as the monetary value of the conditional
transfers increases, psychological distress increases. They find that this effect is
not observed for unconditional transfers, and disappears after the CCT program
has ended, suggesting that transfers to parents that are conditional on the child’s
behavior may negatively affect the child’s wellbeing – although in the case of
Baird et al. (2013), increases in the value of conditional transfers did not result
in reductions in test scores gains relative to the minimum level of transfers
(Baird et al., 2011). Parents may, for instance, use coercive methods to increase
attendance, but only do so as the value of the transfers becomes sufficiently
large. Similarly, here we find no evidence that simply providing parents with
information on the child’s attendance affects test scores negatively, it is only
when parents stand to lose cash transfers from the child’s low attendance that
this leads to ostensibly counterproductive effects on the production of test
scores. This suggests that the introduction of cash incentives rewarding
attendance but not learning distorts parental behavior in such a way as to favor
investments in attendance relative to investments in other learning inputs, at
trend across the school year than that of the transfer treatments (results available
on request).
29
least while the intervention lasts. One way in which parents could induce an
increase in attendance in both the information treatment and the parents’
incentive treatment through strategies leading to differential consequences on
test scores would be for them to be more likely to use a “carrot” (which increases
attendance without adverse consequences on learning) in the information
treatment, and more likely to use a “stick” (which increases attendance but has
negative spillovers on learning) in the parents’ incentive treatment. Although
statistically insignificant, the signs of the estimated effects of the treatments on
consumption of personal goods by the girls are consistent with this theory
(Table A-1), since the effect of the information treatment corresponds to a 6%
increase in consumption of personal goods, but that of the parent treatment
corresponds to a 5.3% decrease in consumption of personal goods.25,26
Table 4 reports impacts of the intervention on a set of pre-specified non-
schooling outcomes (see Appendix A for details about the outcomes specified
at the time of the registration of the trial). In Columns 1 and 5, we test whether
25 It is more difficult to infer the parents’ response to the information component
of the girl voucher treatment from changes in the consumption of personal
goods due to the substitutability between the goods available for purchase with
the vouchers and personal goods not purchased using the vouchers. 26 An alternative explanation would be that different parents respond to the
information and financial incentive components, with increased attendance due
to improved information having a positive effect on test scores, but increased
attendance due to the financial incentive component having no effect or even a
negative effect on test scores. Given the small (statistically insignificant)
difference in the effect of the CCT on attendance relative to the information-
only treatment, the negative effect on test scores coming from the parents
responding only to financial incentives would have to be implausibly large to
fully offset the positive effect of attendance on test scores for parents responding
to additional information.
30
our treatments had any effect on teacher absenteeism. There is no evidence that
changes in teacher attendance may mediate the effects we find on child
attendance and test scores, which gives support to the interpretation of these
effects as resulting from a demand-side response. This also gives reassurance
that the mechanism we set up to ensure that teachers were compensated for the
time spent filling in the report cards (giving 250 meticais’ worth of airtime to
teachers who had filled in the report cards completely at the time of each spot
check) was well-calibrated.
In Columns (2) and (6), we estimate the effect of our treatments on ever
having been married. Given the young age of the targeted girls (12.65, on
average, at baseline), only 2.28% (2.66%) of eligible girls in the household
survey were married at baseline (endline) in the control group. Given the mean
and standard deviation that prevail in the control group, we lack power to detect
realistic reductions in the proportion ever married. The minimum detectable
effect for which we have 80% power is indeed 2.88%-points, which would
require, for instance, the control group to see more than a doubling of the share
ever married compared to baseline while no new girl would form a union in the
treated group. While the point estimates of the effect of the information and the
parents’ treatment on the proportion ever married are large in magnitude, only
the effect of the information treatment is statistically significant at 10% in the
baseline regressions, and it becomes insignificant when controlling for baseline
characteristics (Column (6)).
The remaining columns of Table 4 show tests of whether the treatments
had any effect on the share of girls with an above-median predicted score based
on two separate principal component analyses (PCA). The first variable
measures the self-reported quality of the monitoring exercised by parents on
their children’s school attendance, while the second one measures the extent to
which the girls say that they participate in decisions about their own lives. The
set of interventions evaluated in this experiment had no impact on either
measure.
31
If the self-reported measure of monitoring quality offered a reliable proxy
of actual monitoring quality, then we should see that our treatments increase
self-reported monitoring quality. There are, however, several reasons to believe
that this self-reported variable is a poor proxy. First, there is hardly any variation
in answers to the questions on which the PCA scores are based. At baseline,
only 3.4% (6.6%) of parents answered “neither agree nor disagree” or
“disagree” when asked whether, at the end of each day, they know whether their
daughter was at school (in the classroom), and only 6.2% answered that it had
happened at least once that, on a particular day, they thought that the girl was at
school but actually she was not. This could be due to nearly all parents genuinely
believing that they are perfectly well informed about their child’s school
attendance, but the lack of variation is likely due instead to parents not wanting
to acknowledge openly their lack of control. Indeed, when asked, at baseline,
whether they thought it would be useful to receive a weekly attendance report
card, 80% responded that it would be useful, thus suggesting that most of them
think that their monitoring is not perfect, which contradicts their answers to
direct questions about knowledge of their daughter’s daily attendance.27 We
return to this point in Section IV, where we provide evidence of better
knowledge about daughters’ absences in treatment arms (and especially so in
the parents incentive arm) from comparing the predictive power, across
experimental arms, of the number of absences self-reported by the parent on
whether the girl was absent at school during a spot check.
There is more variation in answers to the questions used to construct the
girl self-reported empowerment index. At baseline, 84.4% of girls reported that
they would be able to keep some item of clothing given to them in exchange of
27 And in a follow-up, open-ended question about why it would be useful to
receive such a report, 98% of those who answered that the weekly attendance
report card would be useful spontaneously responded that it would be helpful in
order to verify the attendance of the child.
32
work done, and the share reporting being involved in decisions concerning them
is 14.6% for health care, 13.2% for visiting relatives, 28.6% for attending
school, and 21.9% for work outside the house. While an increase in parental
information may lead parents to restrict the child’s independence, our measures
of “empowerment”, which mirror those traditionally used to measure the
empowerment of adult women in general-purpose household surveys, seem to
suffer from similar issues to those encountered in the measurement of adult
female empowerment and are thus unlikely to be informative. While difficult to
validate empirically in the absence of objective measures of empowerment,
where such objective measures exist (Almås et al., Forthcoming) or where panel
data exist (e.g., in the PROGRESA evaluation panel), commonly used measures
of adult female empowerment do not perform well. In our sample, the
coefficient of correlation between girls’ answers at baseline and endline for the
five questions used to construct the empowerment index is between -0.06 and
0.16. This is similar, for instance, to the within-household correlation in answers
to a question about whether the wife or the husband is “in charge of household
expenditure” in the PROGRESA evaluation panel.28
To summarize, we find evidence that providing high-frequency
information to parents about their daughter’s school attendance increases school
attendance, and that this effect is not statistically distinguishable from that of a
traditional CCT to parents also providing the same information. Incentivizing
girls with vouchers allowing them to buy a choice of goods is at least as effective
as incentivizing parents with the cash-equivalent of these vouchers – and
importantly, not because parents were able to appropriate the vouchers or
28 After restricting the PROGRESA evaluation sample to households composed
only of mother, father, and children observed in all three survey waves between
October 1998 and November 1999, the correlation coefficient between a binary
indicator for whether the wife (the husband) is “in charge of household
expenditure” and its 6-month lag is 0.040 (0.066) (Sokullu and Valente, 2018).
33
reallocated household expenditure to cancel out the transfer to their daughters.
In terms of learning, the attendance gains from the information and girl
incentives treatments translated into substantial improvements in scores at a
math test, but not the attendance gains from a traditional CCT treatment. None
of the treatments had a robust effect on enrollment (as would be expected given
the timing of the treatment announcements), teacher attendance, early marriage,
self-reported quality of parental monitoring and self-reported girl autonomy.
The next section explores the robustness of these findings.
IV- Robustness Checks Fisher Randomization and joint testing. Our baseline treatment effect
estimates, while consistent with Neyman’s randomization formulas for the
average treatment effect (Athey and Imbens, 2017), are implemented through
regression analysis. For individual tests, the two main issues highlighted by
Young (2016) when relying on asymptotic theorems are related to: (i) high-
leverage (which only arises with the inclusion of covariates) and (ii) clustered
estimates of variance. We were therefore careful to present results that do not
include covariates (other than district fixed effects) or rely on clustered standard
errors. An additional issue which we address using the randomization-based
tests proposed by Young (2016) is that of joint testing of multiple hypotheses.
In Table 5, we report estimates based on exact p-values for the sharp null
hypothesis of no treatment effect for none of the schools in our sample. More
specifically, we report individual p-values for each treatment effect estimate, as
well as for joint tests of, respectively, all treatment effects in each equation, all
treatment effects in each table, and all treatment effects across both results
tables. Differences between exact randomization p-values for individual
significance tests and the estimates reported in the main analysis are very small,
and the same conclusions (and levels of significance) are obtained. Joint tests
confirm the robustness of our findings on schooling outcomes (positive effects
34
on attendance and math score, but not on enrollment) and the absence of
treatment effects on the other outcomes studied.
Correcting for attrition. As reported earlier, attrition of girls taking part
in the household survey was slightly larger in the control group than in the
treated groups. While our main outcome of interest (independently verified
attendance rate at school) and teacher attendance are not affected by this
differential attrition in the household survey, below we present results for the
other outcomes, correcting for differences in individual girls’ probability to
attrit from the household survey. More precisely, in Table 6, we ran regressions
in which the school averages are obtained after weighting each girl in the
endline survey sample by the inverse of the probability that she would be
observed at endline, as predicted by all her individual and household baseline
characteristics summarized in Table 2. Interestingly, none of the outcome
variables measured at baseline predicts attrition, while older girls and girls from
poorer households were more likely to attrit and girls from Manica district (of
Manica province) were less likely to attrit. Reassuringly, reweighting
observations by the inverse of the probability that they attrit does not change
our conclusions.
No selection of girls through school switches. The treatments were
announced after the official enrollment period closed, and, in most cases, after
the start of the school year, so that a negligible effect on enrollment was to be
expected, as confirmed in our data analysis. Another potential source of
selection of girls into the school registers for which the survey firm recorded
spot check attendance data is through school switches. Out of the 2,687 endline
survey girls whose parents reported as being enrolled for the 2016 school year,
only 157 (5.84%) were reported as being enrolled in a school other than the one
they were sampled from. Estimating Equation (4) using, as dependent variable,
a binary indicator equal to one if the girl is reported enrolled in a different school
to that from which she was sampled and zero if she was reported enrolled in her
original school, no treatment indicator is individually significant (nor are they
35
jointly significant).29 As a further robustness check, we re-estimated the effect
of our treatments on attendance, but restricting the sample used to construct the
share of girls present to names registered on the class roll at the first spot check.
The first spot checks were carried out within the two first months of school
(between February 25 and March 31), and so well before any end-of-trimester
transfers were paid. The class rolls called by the independent surveyor were
slightly updated between spot checks for various reasons. A few girls changed
classes or schools during the year, some names were updated to match the girl’s
used name when it did not match that with which she was recorded in the school
register, or to match the name used at home in the case of girls included in the
household survey sample. Estimates obtained by restricting the spot checks data
to girls with exact name matches from the first attendance check roll are
presented in Table 7. These results are near-identical to those obtained in the
main analysis, thus confirming that selection through school switches is
unlikely to be biasing our results.
Ex-post power calculations. In Table 8, we report ex-post power
calculations using the means and standard deviations of the outcomes studied in
this paper in the control group, for 80% power. The last column reports the
Minimum Detectable Effect (MDE) as a share of the control group’s mean,
showing that the experiment is well-powered for our three schooling outcomes,
teacher absenteeism and self-reported monitoring quality, but not for being ever
married and self-reported empowerment. This bolsters our confidence in the
results for which we find consistent significant effects, while confirming the
inconclusiveness of our findings for early marriage and self-reported
empowerment.
29 Individual coefficients (p-values) are: 0.004 (0.784), -0.013 (0.316), 0.0152
(0.237) for the information, parent cash and girl vouchers arms, respectively,
and the joint F-test p-value is 0.183.
36
Controlling for pre-treatment outcomes. As an additional robustness
check, we also present ANCOVA estimates obtained from estimating Equation
(4) with an additional regressor equal to either the value of the outcome at
baseline, where available, or to an available proxy of the outcome at baseline,
when the outcome was not measured at baseline but a reasonable proxy exists.
Using this ANCOVA approach is preferable to Difference-in-Differences even
when the baseline outcome is available, as there is no loss of power when the
correlation between pre- and post-treatment outcomes is low (McKenzie, 2012).
Results in Table 9 show that all our conclusions so far are robust to the inclusion
of these pre-treatment outcomes.
Interpretation of our findings for the information treatment. Here we
present further evidence in support of our interpretation of the effect of the
information treatment as being due to an increase in the quality of parental
monitoring rather than due to some generic “salience” effect of the treatment.
For the girls surveyed in their households who were both (i) (reported by parents
as being) enrolled in school in 2016 and (ii) could be matched to our
independent school attendance records,30 we can evaluate the quality of the
parental monitoring technology by checking the predictive power of the number
of child absences during October 2016 reported by the parent in the household
survey on attendance at the last spot check carried out in schools, which took
place between October 10 and November 3, 2016. Table 10 reports estimates
from a regression of an indicator for whether the girl was absent at the last
independent attendance check on the reported number of days absent during
October 2016 and district fixed effects, experimental arm by experimental arm
(Columns (1) to (4)). On the basis of 22 days of school, if the probability of
being absent was the same in any given day, then an additional day absent
during the month should increase the probability of being absent on the day of
30 77% of girls whose parents said were enrolled could be matched to names in
official school records.
37
the spot check by 1/22=0.045. In the control group, however, the estimated
increase is positi